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Rapid Responses: Rapid Responses published:
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Atherosclerosis, antibiotics and infections: the uncertain road.
- Gustavo E. Sevlever, Sebastian F. Ameriso (27 December 2005)
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Mortality of antibiotic therapy is not higher in stable coronary heart disease
- Hisato Takagi, Maiko Sugimoto, Takayoshi Kato, Yukihiro Matsuno, Takuya Umemoto (7 January 2006)
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CLARICOR - what about the statins?
- Stephen Head (9 January 2006)
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Worrying study ... hang on, do the numbers add up?
- Dr Matthew L Grove (10 January 2006)
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The inability of randomised controlled trials to produce scientifically conclusive results
- Jeffrey Mann (11 January 2006)
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CLARICOR - not clear at all
- Hoong Sern Lim (13 January 2006)
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Does Claricor legitimately test the Chlamydia pneumoniae hypothesis ?
- John DE Parratt (17 February 2006)
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The CLARICOR data are correct
- CLARICOR Trial Group (14 March 2006)
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Bait and Switch
- S. Stanley Young, Mike Last (14 March 2006)
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The CLARICOR analyses were planned
- The CLARICOR Trial Group (9 May 2006)
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Gustavo E. Sevlever, Staff neuropathologist FLENI, Montañeses 2325 Buenos Aires Argentina 1428CKQ, Sebastian F. Ameriso
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26-Dec-05 Dear Srs, We read with great interest the article titled “Randomized placebo controlled multicentre trial to assess short term clarithromycin for patients with stable coronary heart disease: CLARICOR trial” by Jespersen et. al.(1) The relationship between systemic infections and the occurrence of atherosclerosis in various territories is under active research. The exact nature of the association, if any, is not completely elucidated. Infectious processes might act through both systemic effects and/or direct arterial invasion. The infectious process within the vessel wall may be responsible for the initiation, progression, and/or complication of the atherosclerotic plaque. However, the clinical significance of microorganisms resident within the arterial wall or the systemic infection remains unclear. Several different scenarios may arise with quite divergent implications for pathogenesis and therapeutics, and the whole subject may be more complex than originally thought. Clinical trials using antibiotics in patients with vascular disease have provided mostly negative or inconclusive results with few exceptions (2). The multicentre trial of Jespersen et al,(1)showed worse outcome in patients with stable coronary disease who received clarithromycin. The authors suggest a potential cardiotoxic effect of the drug. We and others have found Helicobacter Pilory (HP) in a large number of atherosclerotic carotid plaques (3). Recently, we have also demonstrated substantial HP prevalence as well as expression of the protective enzyme hemoxygenase-1 in plaques obtained from asymptomatic subjects (4). These findings suggest that the presence of HP infection on the atherosclerotic plaque may promote oxidative stress and consequently induce a protective response. We, thus, propose an alternative hypothesis for the detrimental effect of antibiotics in this population. Clarithromycin is effective for the treatment of gastric HP infection (5). Coronary atherosclerotic plaques harbor a substantial number of HP infections (6). We think that clarithromycin administration may exert a deleterious effect in stable patients through HP eradication from coronary plaques. No doubt, much more work is needed in order to clarify the complex relationship between infection, inflammation and the biochemistry of the oxidative stress response. Gustavo Sevlever Sebastian F. Ameriso References 1. Jespersen CM, Als-Nielsen B, Damgaard M, Hansen JF, Hansen S, Helo OH, Hildebrandt P, Hilden J, Jensen GB, Kastrup J, Kolmos HJ, Kjoller E, Lind I, Nielsen H, Petersen L, Gluud C, Jespersen CM. Randomised placebo controlled multicentre trial to assess short term clarithromycin for patients with stable coronary heart disease: CLARICOR trial. BMJ, doi:10.1136/bmj.38666.653600.55 (published 8 December 2005) 2. Anderson J, Infection, Antibiotics, and Atherothrombosis — End of the Road or New Beginnings? N Engl J Med 352;16: 1707-1708 3. Ameriso SF, Fridman EA, Leiguarda RC, Sevlever GE. Detection of Helicobacter pylori in human carotid atherosclerotic plaques. Stroke. 2001 Feb;32(2):385-91. 4. Ameriso SF, Villamil AR, Zedda C, Parodi JC, Garrido S, Sarchi MI, Schultz M, Boczkowski J, Sevlever GE.Heme oxygenase-1 is expressed in carotid atherosclerotic plaques infected by Helicobacter pylori and is more prevalent in asymptomatic subjects. Stroke. 2005 Sep;36(9):1896-900. Epub 2005 Aug 11. 5. Hopkins RJ. Current FDA-approved treatments for Helicobacter pylori and the FDA approval process. Gastroenterology. 1997 Dec;113(6 Suppl):S126-30. 6. Adiloglu AK, Ocal A, Can R, Duver H, Yavuz T, Aridogan BC. Detection of Helicobacter pylori and Chlamydia pneumoniae DNA in human coronary arteries and evaluation of the results with serologic evidence of inflammation. Saudi Med J. 2005 Jul;26(7):1068-74. Competing interests: None declared |
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Hisato Takagi, Consultant Cardiovascular Surgeon Department of Cardiovascular Surgery, Shizuoka Medical Centre, Shizuoka 411-8611, Japan, Maiko Sugimoto, Takayoshi Kato, Yukihiro Matsuno, Takuya Umemoto
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We read with great interest results of the CLARICOR trial (1) regarding short term clarithromycin for patients with stable coronary heart disease. All cause mortality was significantly higher in the clarithromycin group. Although several trials on antibiotic therapy including clarithromycin, azithromycin, roxithromycin, or gatifloxacin, in patients with coronary heart disease have been published, no meta-analysis of trials in patients with stable coronary heart disease has been conducted. Therefore, we performed a meta-analysis of prospective, randomized, placebo-controlled trials of antichlamydial antibiotic treatment in patients with stable coronary heart disease. Comprehensive searches of the MEDLINE and Cochrane Central Register of Controlled Trials databases were performed using Web-based search engines (OVID, PubMed) for human studies published in English between 1996 and 2005. Our search identified a total of 5 trials (1-5) for inclusion in the meta-analysis. All cause mortality outcomes were presented in 5 trials that enrolled 16 468 patients. A nonsignificant reduction in mortality was observed in 2 trials (2,4). The combines mortality rate was 6.5% among treated patients versus 6.0% of participants in the placebo group (odds ratio, 1.08; 95% confidence interval, 0.93- 1.26; P = 0.30; using a random-effects model). There was minimal quantitative heterogeneity of results (P = 0.31) and no evidence of significant publication bias (P = 0.62; using an adjusted rank-correlation test). Although exclusion of any single trial of 4 trials (1-3,5) form the analysis did not alter the overall findings of this analysis, exclusion of the WIZARD trial (4) form the analysis demonstrated that mortality was significantly higher in the treated patients (1.18; 1.01-1.39; P = 0.04). Despite results of the CLARICOR trial, our meta-analysis of 5 trials in patients with stable coronary heart disease demonstrated that antibiotic therapy had no impact on all cause mortality among treated versus untreated patients. 1. Jespersen CM, Als-Nielsen B, Damgaard M, Hansen JF, Hansen S, Helo OH, et al. Randomised placebo controlled multicentre trial to assess short term clarithromycin for patients with stable coronary heart disease: CLARICOR trial. BMJ 2006;332:22-7. 2. Gupta S, Leatham EW, Carrington D, Mendall MA, Kaski JC, Camm AJ. Elevated Chlamydia pneumoniae antibodies, cardiovascular events, and azithromycin in male survivors of myocardial infarction. Circulation 1997;96:404-7. 3. Muhlestein JB, Anderson JL, Carlquist JF, Salunkhe K, Horne BD, Pearson RR, et al. Randomized secondary prevention trial of azithromycin in patients with coronary artery disease: primary clinical results of the ACADEMIC study. Circulation 2000;102:1755-60. 4. O'Connor CM, Dunne MW, Pfeffer MA, Muhlestein JB, Yao L, Gupta S, et al. Azithromycin for the secondary prevention of coronary heart disease events: the WIZARD study: a randomized controlled trial. JAMA 2003;290:1459-66. 5. Grayston JT, Kronmal RA, Jackson LA, Parisi AF, Muhlestein JB, Cohen JD, et al. Azithromycin for the secondary prevention of coronary events. N Engl J Med 2005;352:1637-45. Competing interests: None declared |
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Stephen Head, General Practice Performer Middleton Lodge, New Ollerton, Newark, Nottinghamshire, NG22 9SZ.
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Unless contraindicated it would be expected all patients entered in this trial would be taking a statin, yet there is no mention of this in the publication. Were these drugs continued or suspended during the course of antibacterial? There is a well recognised major interaction between the macrolides and statins. The British National Formulary advises that concommittant therapy should be avoided and it is common practice to suspend statin therapy whilst using these antibiotics. What did the CLARICOR trialists do and what are the implications for the use of Clarithromycin for intercurrent infections in patients with Coronary Heart Disease? If they continued the statin, this might be the explanation of the observed excess mortality. Clarithromycin is a most useful drug for vulnerable patients in the community with respiratory infections and clarification of this issue is urgently needed. Competing interests: None declared |
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Dr Matthew L Grove, Consultant Rheumatologist NTGH, NE29 8NH
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Dear Sir I read this study with interest and mounting alarm. A quick back-of- the envelope calculation yields an NNH of 58 (95%ci 30-2400 odd) for all cause mortality based on the figures in Table 3 - ie, a two week course of clarithromycin given to patients with ischaemic heart disease may kill as many as one in sixty within three years or so. But there appear to be some discrepancies between Tables 2 and 3 (or at least, on BMJ.com where I read the paper): In Table 2, "all cause mortality" is given as 184/2172 treated patients and 159/2200 placebo patients. In Table 3, it is given as 212/2172 treated patients and 172/2200 placebo. Similarly, "cardiovascular mortality" in the treated group is variously reported as 89/2172, 83/2172 and 111/2172, in, respectively, the secondary composite outcome section of Table 2, the tertiary composite outcome measure section of Table 2, and in Table 3. Similar discrepancies are given for the placebo group. By contrast, the same numbers are given for "myocardial infarction/ unstable angina" in Table 2 for the primary and secondary composite outcomes, but then a different set of numbers in the tertiary composite outcome. Could the authors explain the discrepancy? Have I missed something? Competing interests: None declared |
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Jeffrey Mann, Retired physician Salt Lake City, UT 84103
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Many people incorrectly think of a RCT as being a scientific experiment that can definitively demonstrate that a drug causes an increased, or decreased, risk of an outcome event such as death. However, that opinion is only scientifically valid if the trialists can guarantee that chance events do not play a significant role by creating an imbalance in unrecognised prognostic variables between the treated and control patients, thereby causing the two groups to have a different likelihood of a mortality event. Regarding the CLARICOR trial [1], the trialists stated-: "We found no beneficial effect of short term clarithromycin for patients with stable coronary heart disease. On the contrary, the significantly increased cardiovascular mortality in the clarithromycin treated patients surprised us." That statement obviously implies that the trialists had an expectation bias regarding the anticipated effect of clarithromycin on CV mortality, because they unequivocally state that they didn't expect clarithromycin to increase the CV mortality. They subsequently proffer an explanation to account for the unexpected CV mortality result when they state -"Furthermore, we cannot exclude chance imbalance at randomisation or after randomisation as a cause of the increased mortality." In other words, the trialists are conceding that chance event effects could have affected their trial's results to a significant degree, and that chance event effects could have produced the unexpected CV mortality result. Trialists often bring up the possibility of chance event effects in low control event trials when they get unfavorable results, and they do not do so when they get favorable results. If the CLARICOR trial demonstrated that clarithromycin decreased the CV mortality rate, then the trialists presumably would have concluded that there was a direct causal link between drug exposure and a favorable CV mortality outcome, and they presumably would not have brought up the possibility of chance event effects. However, that particular conclusion would surely be a manifestation of scientific hypocrisy, because if the trialists state that chance event effects could have played a significant role in this trial that produced an unexpected unfavorable result (due to a small sample size relative to a low mortality control event rate of ~5%), then chance event effects should have an equal likelihood of producing an expected favorable result. If trialists can always bring up the theoretical possibility of chance events affecting their trial's results when they get unfavorable results, rather than favorable results, then it implies that a RCT is not a neutral scientific experiment that can consistently produce scientifically repeatable results. This situation of scientific uncertainty is compounded by the fact that all trials have a finite duration. The trialists stated-: "We found a gradually increasing outcome rate in the clarithromycin patients. If we had stopped follow-up at one year, we would have had a neutral result like most other trials." In other words, the trialists are admitting that their trial could produce variable CV mortality results depending on its duration, and that the "degree" of favorable (or unfavorable) CV mortality effect could simply be altered by varying the trial's duration. That disturbing fact introduces yet another confounding variable that challenges the legitimacy of any person's belief that a RCT is a neutral scientific experiment that can produce consistent results. The reason that a RCT studying CV mortality for a time period of approximately 3 years can produce variable results from month-to-month is simply due to the natural phenomenon of chance variability in the likelihood of mortality events from month-to-month during a 36 month time period. In other words, there is no logical reason why the placebo or treated patients should have exactly the same risk of death in each one month period of a 36 month trial. Therefore, it must be scientifically futile to look for a definitive causal link association by painstakingly examining the CV mortality results for each 1-month time period of a 36 month trial. The trialists wrote-: "We did not observe differences in cardiovascular mortality during the first month, and drug interactions cannot readily explain the observed difference in cardiovascular mortality." Can one conclude that the trialists are scientifically sophisticated when they state-: "we did not observe differences in cardiovascular mortality during the first month"? Surely, any observed CV mortality difference during any 1 month time period of a 36 month trial is much more likely to be distorted by chance event effects (as compared to the entire trial period)? If the trialists readily concede that chance event effects could have affected the trial's overall CV mortality results for the entire trial time period of ~36 months, then it is even more scientifically irrational to search for a definitive causal link association in any 1-month time period. The trialists also attempted to enhance the scientific legitimacy of their trial's CV mortality results by comparing their trials' CV mortality results to the CV mortality results from other clarithromycin trials. The trialists stated-: "Only two other trials have assessed clarithromycin in patients with coronary heart disease. The CLARIFY trial randomised 148 patients to clarithromycin or placebo for three months. The clarithromycin group had an insignificantly raised 1.5 year mortality (odds ratio 4.17, 95% confidence interval 0.46 to 38.2). Berg et al randomised 473 patients to clarithromycin or placebo until the day of coronary artery bypass grafting. Two year mortality was insignificantly raised in the clarithromycin patients (1.10, 0.44 to 2.76)". Do you think that a mini-metanalysis of three significantly underpowered clarithromycin trials produces a more scientifically conclusive result than the single result from the underpowered CLARICOR trial? If the trialists concede that the CLARICOR trial could have been significantly affected by chance event effects, then I think that it is irrational to introduce additional evidence from another clarithromycin trial, which was much more likely to have been influenced by chance event effects. The CLARIFY trial only consisted of 148 patients and the trial duration was only 3 months. Therefore, the CLARIFY trial was much more likely to be affected by chance event effects than the CLARICOR trial, and the degree of scientific uncertainty surrounding the CLARIFY trial's results is incontestably evident in its wide 95%CI odds ratio range results, which varied from an OR of 0.46 to an OR of 38.2. The CLARIFY trial's results are so scientifically inconclusive that it is reasonable for a rational person to conclude that the CLARIFY trial cannot even be regarded as being a legitimate scientific experiment. Therefore, the uncertainty regarding the scientific legitimacy of the CLARICOR trial's CV mortality results can only be heightened by introducing scientifically uncertain evidence from another more scientifically inconclusive clarithromycin trial. Penston argues [2]-: "We have been lulled into the twilight world of large-scale randomised trials, inhabited by mere shadows of a therapeutic benefit. It is a world of a flawed, pseudo-scientific methodology blurred by a fog of statistical mumbo–jumbo, and one in which dubious claims stand secure in the absence of any effective means to challenge their validity. It is a world more suited to quacks and charlatans than to the scientists and clinical researchers who have been responsible for so many genuine advances." I think that Penston's controversial ideas regarding the methodological weaknesses of large-scaled randomised controlled trials deserve much greater attention. Jeff Mann, MD. References: 1. Christian M Jespersen, Bodil Als-Nielsen, Morten Damgaard, Jørgen Fischer Hansen, Stig Hansen, Olav H Helø, Per Hildebrandt, Jørgen Hilden, Gorm B Jensen, Jens Kastrup, Hans Jørn Kolmos, Erik Kjøller, Inga Lind, Henrik Nielsen, Lars Petersen, Christian Gluud, CLARICOR Trial Group. Randomised placebo controlled multicentre trial to assess short term clarithromycin for patients with stable coronary heart disease: CLARICOR trial. BMJ 2006;332:22-27, doi:10.1136/bmj.38666.653600.55 (published 8 December 2005). 2. Penston, James. Large-scale randomised trials - a misguided approach to clinical research. Medical Hypotheses. 2005;64(3):651-7. Competing interests: None declared |
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Hoong Sern Lim, SpR Cardiology Sandwell General Hospital B71 2HJ
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Jespersen and colleagues suggest that 2 weeks of treatment with clarithromycin may increase the risk of cardiovascular mortality in patients with established but stable coronary artery disease [1]. However, cardiovascular mortality only started diverging significantly after 400 days (from the Kaplan-Meyer curves). This would suggest either a clarithromycin-mediated alteration in atherosclerotic pathophysiology, with consequent (late) increased cardiovascular mortality or more likely, uncontrolled confounding factors intervening after randomisation. As no follow-up visits were planned in this study, crucial information on blood pressure and lipid control are not available. Aggessive blood pressure (perhaps ACE inhibitors in particular) and lipid management have well-documented benefits in patients with established coronary artery disease. At study entry, only about 41% and 27% of patients were taking statins and ACE inhibitors. It is not clear if statin and ACE inhibitor use increased during the study period, or indeed if their use were comparable in both treatment arms throughout the study period. Finally, the authors suggested increased mortality with antibiotic use by pooling their data with other studies. The validity of such analysis is questionable given the clear differences in study designs. The PROVE-IT study tested regular intermittent courses of a quinolone (not a macrolide) over a mean of 2 years (not a single 2-week course) in patients with an acute coronary syndrome in the preceding 10 days (patients excluded in the CLARICOR study) [2]. These study limitations clearly preclude any firm conclusions on the safety (or otherwise) of clarithromycin in patients with coronary disease. In this regard, the authors' cautious assertion that the "long term safety of clarithromycin in patients with coronary heart disease needs further evaluation" is appropriate. References 1. Jespersen CM, Als-Nielsen B, Damgaard M, et al. Randomised placebo controlled multicentre trial to assess short term clarithromycin for patients with stable coronary heart disease: CLARICOR trial. BMJ 2006; 332: 22-7. 2. Cannon CP, Braunwald E, McCabe CH, et al. Antibiotic treatment of chlamydia pneumoniae after acute coronary syndrome. N Engl J Med 2005; 352: 1646-54. Competing interests: None declared |
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John DE Parratt, Neuroimmunology Research Fellow Department of Neurology, University of Sydney, NSW 2006, Australia
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Jespersen and colleagues (1) examined the effect of Clarithromycin treatment in patients with stable coronary heart disease (CHD). Clarithromycin was associated with increased cardiovascular mortality. There appeared to be no beneficial effects of antibiotic therapy in CHD patients infected with Chlamydia pneumoniae. Although not entirely explicit, the authors’ postulated pre-hoc, any improvement in cardiovascular mortality may be secondary to eradication or suppression of C pneumoniae infection. However, evidence of infection was not necessary for patient inclusion. Accordingly, the frequency of infection in treatment and placebo arms was unknown. Post-hoc, C pneumoniae IgG antibodies were found in approximately 60% of each group and IgA antibodies in 20%. Antibody measurements were not effected by treatment but this is not surprising because elevated single specimen IgG titres usually represent past exposure to C pneumoniae. IgA antibodies may be a better surrogate marker of chronic infection but this is not certain (2). In general, serological measurements are not recommended for the diagnosis of chronic C pneumoniae infection (2). Several large double-blinded placebo controlled antibiotic trials have attempted to clarify the role of C pneumoniae in CHD with conflicting results (3). Only a few trials have used evidence of C pneumoniae infection as inclusion criteria (and these were dependent on antibody measurements). If the actual percentage of infected patients is small, any treatment effect will be obscured by the CHD population examined, at large. Like Jespersen et al (1), most of these trials and subsequent meta- analyses, determined that antibiotic treatment of all CHD patients is not beneficial and in the main, not harmful (3). Now it is necessary to determine whether CHD patients with C pneumoniae infection may benefit, as a sub-cohort, from antibiotic treatment. Serum antigen specific methods to detect C pneumoniae infection are available (4) and should be used to screen future populations for inclusion in placebo controlled trials. 1. Jespersen CM, Als-Nielsen B, Damgaard M, Hansen JF, Hansen S, Helo OH, et al. Randomised placebo controlled multicentre trial to assess short term clarithromycin for patients with stable coronary heart disease: CLARICOR trial. BMJ 2006;332:22-7. 2. Dowell SF, Peeling RW, Boman J, Carlone GM, Fields BS, Guarner J et al. Standardizing Chlamydia pneumoniae Assays: Recommendations from the Centers for Disease Control and Prevention (USA) and the Laboratory Center for Disease Control (Canada). Clin Infect Dis 2001;33:492-503. 3. Andraws R, Berger JS, Brown DL. Effect of Antibiotic Therapy on Outcomes of Patients With Coronary Artery Disease. A Meta-analysis of Randomized Controlled Trials. JAMA 2005; 293:2641-2647. 4. Tavendale R, Parratt D, Pringle SD, A'brook R, Tunstall-Pedoe H.Serological markers of Chlamydia pneumoniae infection in men and women and subsequent coronary events; the Scottish Heart Health Study. Eur Heart J. 2002 Feb;23(4):301-7. Competing interests: None declared |
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CLARICOR Trial Group, See paper Copenhagen
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The CLARICOR data are correct EDITOR – We thank for the interest in our CLARICOR trial (1) and the comments that have been raised in the rapid responses. Sevlever and Ameriso suggest that the negative effect of clarithromycin on survival in CLARICOR patients (1) may be due to a paradoxical mechanism by which eradication of, eg, Helicobactor (H) pylori from atherosclerotic plaques may destabilise the plaques and therefore increase the risk of cardiovascular atherothrombotic events. The hypothesis deserves further scrutiny. We have not studied inflammation markers or H pylori antibodies in the CLARICOR trial, so we cannot offer further information at present. Takagi et al performed a meta-analysis of 5 trials of antichlamydial antibiotic treatment in patients with stable coronary heart disease. They found a nominal but statistically insignificant higher mortality in macrolide-treated patients, and concluded that the antibiotics did not influence mortality in such patients. We do not question the correctness of the analysis by Takagi et al. There are, however, significant differences between trials regarding choice of antibiotic (four trials used azithromycin and only the CLARICOR trial used clarithromycin) and duration of follow-up. Takagi et al’s sensitivity analyses demonstrate that the results depend on which trials are included. When the WIZARD trial (2) was excluded, the pooled mortality risk was significantly raised by macrolide antibiotics (odds ratio 1.18; 95% confidence interval 1.01 to 1.39, P = 0.04). Interestingly, the WIZARD trial is the one trial with the shortest follow-up (14 months) of the five trials (2). This was exactly the point we wanted to make in our discussion, when we pooled the trials with follow up for more than 24 months (1). When we pooled the data of the three trials following patients for more than 24 months (PROVE-IT (3), ACES (4), and CLARICOR (1)), administration of antibiotics was also associated with a significantly increased mortality (1.20, 1.04 to 1.39). We are following the CLARICOR population regarding all-cause mortality, and relative risks may change over time. The verdict is still pending. Head mentions the well-known pharmacokinetic interaction between statins and macrolide antibiotics that may increase statin concentrations by decreasing statin clearance. This interaction was not taken into consideration when administering clarithromycin. We have performed additional analyses on the interaction between statins and clarithromycin and we can assure Head that we do not see an interaction of the kind suggested. These data are about to be submitted for publication. Grove calculates a number needed to harm of 1 in 60 during three years, which matches our own calculation, which results in 7 additional deaths during 1000 years of follow-up (95% confidence interval 2-12 deaths) (1). The discrepancy between Tables 2 and 3 noted by Grove is due to the fact that in analysis of time to death, all deaths are counted (n = 384). But in the analysis of time to first event (the composite outcome measures) only those deaths that are the first event are listed and included in the analysis (n = 343). This was stated in the footnote of Table 2. So the numbers in the CLARICOR trial are correct and we suggest that Grove hang on. Mann chides us for stating the possibility that the unexpected adverse effect of clarithromycin could be brought about by ‘the cruel play of chance’. If our trial had had the opposite result, would we (and Mann!) really have considered this phenomenon? This is an important general point, which we have considered at length. Firstly, the credibility of any study is increased if the results confirm the first alternative trial hypothesis (ie, that experimental is better than placebo). Secondly, we took both alternative hypotheses into account during the planning of the trial by using two-tailed alpha of 0.05 and as stated in the paper: “The code was not broken until all main analyses were completed and a two way main conclusion formulated” (1). We therefore reject Mann’s assertion. Mann further questions our wording as regards the effect of follow-up time on mortality. We are very much aware of that and have done our utmost to avoid any phrase that might suggest that we attached any importance to the wiggles of the curves depicting the accrual of events over time. In view of the effect of macrolide antibiotics on cardiac repolarisation, we obviously needed to look closely on mortality during treatment and the time following closely after end of treatment. Any immediate adverse effect on mortality would have suggested a proarrhytmic mechanism. But we did not see that (1). Finally, Mann objects to our comparison of the CLARICOR trial results with other trials on clarithromycin in similar patients. A major principle of meta-analysis is to pool the data of smaller trials to increase the power and precision of the total trial experience. In fact, this is how our assessment of interventions ought to be conducted (5,6). The use of ACE inhibitors, statins, and other drugs was well balanced across the treatment arms at entry. In our report we admit that, as all follow-up was through public registers, “we cannot exclude chance imbalances” with respect to medication or lifestyle that may have crept in during the study period (1). Lim comes back to this point. It should be clearly understood that this element of uncertainty does not detract from the conclusions of the CLARICOR trial. The (randomisation-based) P-values and confidence intervals already cover it. It is not an element of uncertainty that adds uncertainty to the already reported level of statistical uncertainty. It is just one of the many elements of uncertainty that could have been reduced by a more expensive follow-up scheme. We agree with Lim that pooling of data from trials using different antibiotics may be questionable, but as discussed above with Takagi et al the situation for long-term trials of macrolides only does not clear the sky. Only more data may do that. Parratt is correct that we likely included patients with and without Chlamydia (C) pneumoniae infection of the coronary arteries. We think, however, that Parratt has overestimated the discriminatory capacity of serological markers of C pneumoniae infection. Neither immunoglobulin (Ig) G, IgA, and IgM antibodies nor circulating immune complexes with C. pneumoniae antigen were able to significantly predict subsequent coronary events in the study by Tavendale et al (7). Even if we had valid tests for picking out the true bacteria carriers, it would only mean that one could conduct more informative trials of the effects of antibiotics. It would not detract from the validity of the CLARICOR results: it would only indicate that the same information might have been obtained with fewer participants and more expensive testing of candidate participants. The CLARICOR Trial Group The Departments of Cardiology, Copenhagen Hospital Corporation, Copenhagen University Hospital, Department of Clinical Microbiology, Odense University Hospital, Statens Serum Institut, Copenhagen, Department of Cardiology, Herlev Hospital, Copenhagen University Hospital, Department of Biostatistics, Institute of Public Health, Faculty of Health Sciences, University of Copenhagen, and The Copenhagen Trial Unit, Centre for Clinical Intervention Research, H:S Rigshospitalet, Copenhagen University Hospital, DK-2100 Copenhagen, Denmark. REFERENCES 1. Jespersen CM, Als-Nielsen B, Damgaard M, Fischer Hansen J, Hansen S, Helø OH, et al. Randomised placebo controlled multicentre trial to assess short term clarithromycin for patients with stable coronary heart disease: CLARICOR trial. BMJ 2006; 332:22- 27; doi:10.1136/bmj.38666.653600.55; doi:10.1136/bmj.38666.653600.55. 2. O'Connor CM, Dunne MW, Pfeffer MA, Muhlestein JB, Yao L, Gupta S, et al. Azithromycin for the secondary prevention of coronary heart disease events: the WIZARD study: a randomized controlled trial. JAMA 2003;290:1459-66. 3. Cannon CP, Braunwald E, McCabe CH, Grayston JT, Muhlestein B, Giugliano RP, et al. Antibiotic treatment of Chlamydia pneumoniae after acute coronary syndrome. N Engl J Med 2005;352: 1646-54. 4. Grayston JT, Kronmal RA, Jackson LA, Parisi AF, Muhlestein JB, Cohen JD, et al. Azithromycin for the secondary prevention of coronary events. N Engl J Med 2005;352: 1637-45. 5. Higgins JPT, Green S, editors. Cochrane Handbook for Systematic Reviews of Interventions 4.2.5 [updated May 2005]. In: The Cochrane Library, Issue 3, 2005. Chichester, UK: John Wiley & Sons, Ltd. 6. Young C, Horton R. Putting clinical trials into context. The Lancet 2005;366 (9480):107-108. 7. Tavendale R, Parratt D, Pringle SD, A'brook R, Tunstall-Pedoe H. Serological markers of Chlamydia pneumoniae infection in men and women and subsequent coronary events; the Scottish Heart Health Study. Eur Heart J 2002;23(4):301-7. Competing interests: None declared |
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S. Stanley Young, Statistician NISS, RTP NC 27709, Mike Last
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How many tries do you get for statistical significance and still expect the reader to believe your conclusions? Jespersen et al. (1) ran a prospective, blind, randomized trial testing the hypothesis that antibiotic treatment would be beneficial for heart attack survivors (all cause mortality, myocardial infarction, or angina pectoris). Neither their primary or secondary variables were statistically significant. Normally, it would be “game over” however, the investigators decided to poke through the data chasing for “statistical significant” effects. Finding some marginally significant effects they then shifted their conclusions from the “no-effect on primary and secondary endpoints” to a non pre-planned comparison. They hide behind the usual fig leaf, “may cause,” and give the usual sop, asking for more work to be done. There are serious flaws in this usual “epidemiologic” examination of data, specifically there are increased false positive results do to multiple testing (2). Ioannidis (3) reports that 5/6, ~80%, of high impact epidemiology studies examined failed to replicate (multiple testing is likely a major cause of this failure to replicate). Even a modest correction for multiple testing (assuming all tests are independent) results in an adjusted p-value of 0.087 instead of the 0.03 reported. This assumes that only the three hypotheses listed were tested. The statistical analysis strategy and the reporting of this study are fatally flawed; the conclusions are unlikely to replicate and can be safely ignored. S. Stanley Young Mike Last National Institute of Statistical Sciences 1. BMJ, doi:10.1136/bmj.38666.653600.55 2. Pocock SJ, Collier TJ, Dandreo KJ, de Stavola BL, Goldman MB, L. Kalish A, Kasten LE, McCormack VA. Issues in the reporting of epidemiological studies: a survey of recent practice. BMJ 2004; 329: 883- 888. 3. Ioannidis JPA. Contradicted and initially stronger effects in highly cited clinical research. JAMA 2005; 294: 218-228. Competing interests: None declared |
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The CLARICOR Trial Group, Copenhagen Trial Unit DK 2100 Rigshospitalet, Centre for Clinical Intervention Research, Copenhagen University Hospital
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Young and Last raise their index fingers and postulate that we have been hunting game in our analyses of the CLARICOR trial (1). Young and Last could probably not be more wrong! We conducted carefully planned, blinded analyses of the CLARICOR trial data with analyses of the primary, secondary, and tertiary outcome measures as defined in our report of the trial results (1). However insignificant these analyses are felt by Young and Last to have come out, they must concede to the following. First, we have to analyse the individual components of a composite outcome measure to fully understand the effect of clarithromycin on the composite outcome. Second, we owe it to the community to examine serious adverse events in depth (1). In both instances mortality and cardiovascular mortality are highly relevant. The low (and unfavourable) P values we observed cannot be regarded as unearthed by repeated statistical digging. These P-values represent first-rank comparisons. Young and Last point out that we did not work with adjusted P values. This is a highly debated topic (2). However, there are no hidden statistical comparisons of higher priority in our paper, so readers can, if they feel that adjustment is appropriate, carry out the adjustment themselves. Incidentally, even adjusting our P values by multiplying them by 3 or 4 would still leave cardiovascular mortality significantly higher in the clarithromycin-treated compared with the placebo-treated patients (hazard ratio 1.45, 95% confidence interval 1.09 to 1.92) (unadjusted P = 0.011; Bonferroni-adjusted P = 0.044). As to the scientific guidance provided by P values, we agree that P- value adjustments reduce the type I error risk, but at the same time they increase the risk of type II errors. Note also that precise P values and confidence intervals enable more refined research conclusions than simply employing cut-off levels as Young and Last suggest. We found a P value of 0.08 for the primary outcome measure (all cause mortality, acute myocardial infarction, or unstable angina) favouring placebo (hazard ratio 1.15, 95% confidence interval 0.99 to 1.34). A judicious interpretation takes into account not just such naked statistics but also: the direction of finding, its magnitude (eg, mortality of 212 clarithromycin patients versus 172 placebo patients), the methodological quality of the trial, and the findings of other randomised trials. As described in our discussion (1) and our responses to previously raised comments about pooling of our CLARICOR data with those from other trials, these pooled analyses all support our findings. In sum, we find the Young-Last assessment to be lacking in finesse. We, too, hope that Young and Last's prediction for the future is correct. It may be true that an unfavourable conclusion of the present kind is unlikely to replicate, although, according to Ioannidis (3), the instances of published research findings being subsequently disproved are mostly favourable effects of the experimental intervention. This is in accordance with the way systemic errors (bias) are normally taking us (3- 8). Anyhow, our CLARICOR findings are too serious to allow the medical profession to count on the prediction of Young and Last. Iatrogenic harm is under-estimated and under-researched: the more you look for data on adverse events, usually the more you uncover (9). We maintain that until convincing data are presented supporting their prediction, one should be cautious with prescribing clarithromycin, at least to patients with stable ischaemic heart disease. We need more data before we (safely) know who has the fatally flawed position. The CLARICOR Trial Group The Departments of Cardiology, Copenhagen Hospital Corporation, Copenhagen University Hospital, Department of Clinical Microbiology, Odense University Hospital, Statens Serum Institut, Copenhagen, Department of Cardiology, Herlev Hospital, Copenhagen University Hospital, Department of Biostatistics, Institute of Public Health, Faculty of Health Sciences,University of Copenhagen, and The Copenhagen Trial Unit, Centre for Clinical Intervention Research, H:S Rigshospitalet, Copenhagen University Hospital, DK-2100 Copenhagen, Denmark. References 1. Jespersen CM, Als-Nielsen B, Damgaard M, Fischer Hansen J, Hansen S, Helø OH, et al. Randomised placebo controlled multicentre trial to assess short term clarithromycin for patients with stable coronary heart disease: CLARICOR trial. BMJ 2006; 332:22- 27; doi:10.1136/bmj.38666.653600.55; doi:10.1136/bmj.38666.653600.55. 2. Cleophas TJ. Clinical trials: Renewed attention to the interpretation of the P values - review. Am J Ther 2004;11(4):317-22. 3. Ioannidis JP. Contradicted and initially stronger effects in highly cited clinical research. JAMA 2005;294:218-228. 4. Wood L, Sterne J, Jüni P, Egger M. The smaller the study the larger the effect: meta-epidemiological study of randomised controlled trials. 11th International Cochrane Colloquium, Barcelona 2003:49. 5. Als-Nielsen B, Chen W, Gluud LL, Siersma V, Hilden J, Gluud C. Are trial size and reported methodological quality associated with treatment effects? Observational study of 523 randomised trials. 12th International Cochrane Colloquium, Ottawa 2004:102-3. Available at: http://pubhealth.ku.dk/~vosi/files/P-003.ppt. Accessed January 23, 2006. 6. Montori VM, Devereaux PJ, Adhikari NK, Burns KE, Eggert CH, Briel M, et al. Randomised trials stopped early for benefit: a systematic review. JAMA 2005;294: 2203-9. 7. Kjaergard LL, Villumsen J, Gluud C. Reported methodological quality and discrepancies between large and small randomized trials in meta-analyses. Ann Intern Med 2001;135:982-9. 8. Ioannidis JP. Why most published research findings are false. PLoS Med. 2005:e124. Epub 2005 Aug 30. 9. Ioannidis JP, Mulrow CD, Goodman SN. Adverse events: the more you search, the more you find. Ann Intern Med. 2006;144(4):298-300. Competing interests: None declared |
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